Change in noncalcified plaque volume \(\Delta \text{NCPV}\) was the outcome:

\[ \Delta \text{NCPV} = \text{NCPV}_{1} - \text{NCPV}_0 \]

They regressed \(\Delta \text{NCPV}\) directly on baseline values, for example:

\[ \Delta \text{NCPV} = \alpha + \beta \, \text{NCPV}_0 + \varepsilon \]

• Obscures clinically meaningful patterns
  
• Inflates error, reducing model precision
  
• Introduces Mathematical Coupling

• Simulated data (N = 100) approximates ApoB and \(\text{NCPV}_0\) based on summary stats from study
  
• We compare model: ΔNCPV ~ ApoB with NCPV₁ ~ NCPV₀ + ApoB

\(\beta = \frac{\operatorname{Cov}(\Delta \text{NCPV},\ \text{NCPV}_0)}{\operatorname{Var}(\text{NCPV}_0)} = \frac{\operatorname{Cov}(\text{NCPV}_1 - \text{NCPV}_0,\ \text{NCPV}_0)}{\operatorname{Var}(\text{NCPV}_0)}\)

\(= \frac{\operatorname{Cov}(\text{NCPV}_1,\ \text{NCPV}_0) - \operatorname{Var}(\text{NCPV}_0)}{\operatorname{Var}(\text{NCPV}_0)} = \frac{\rho\, \sigma_1 \sigma_0 - \sigma_0^2}{\sigma_0^2}\)

\(= \frac{\rho\, \sigma_1 - \sigma_0}{\sigma_0} = \rho \cdot \frac{\sigma_1}{\sigma_0} - 1\)

where:

• \(\rho = \operatorname{Cor}(\text{NCPV}_0,\ \text{NCPV}_1)\)
• \(\sigma_0\), \(\sigma_1\) = SDs at baseline and follow-up

“Statisticians have repeatedly warned against correlating/regressing change with baseline due to two methodological concerns known as mathematical coupling and regression to the mean.” - Tu & Gilthorpe, 2007

“Mathematical coupling can lead to an artificially inflated association between initial value and change score when correlation or regression is used.” - Brown, 2009

“Many authors and pharmaceutical clinical trialists make the mistake of analyzing change from baseline instead of making the raw follow-up measurements the primary outcomes, covariate-adjusted for baseline.” - Frank E Harrell Jr, PhD, Professor of Biostatistics

Additionally, Table 3 does include one multivariable regression on the primary outcome \(\Delta \text{NCPV}\):

• \(\Delta \text{NCPV} = \alpha + \beta_1 \, \text{CAC}_{\text{bl}} + \beta_2 \, \Delta \text{ApoB} + \beta_3 \, (\text{CAC}_{\text{bl}} \times \Delta \text{ApoB}) + \varepsilon\)
• Appears to be the only adjusted model involving \(\Delta \text{NCPV}\)

So they did include three multivariable models multivariable models: One on the main outcome \(\Delta \text{NCPV}\) and two in their Age Mediation Analysis on NCPV at follow-up.

None tested the full set of available covariates, nor explained why these specific models were chosen.

This selective modeling raises questions.

Assuming there is no true association between ApoB and ΔNCPV, how likely is it that we’d observe a slope as large (or larger) than the one we found, just by chance?

If p-value (p > 0.05) a frequentist analysis can say:

“We did not find sufficient evidence to reject the hypothesis that ApoB has no association with ΔNCPV”

It cannot say the null is likely true, or produce the probability that there is no association, just that the data were inconclusive.

How well do the data fit under two competing models, one with no association (null), and one with a range of plausible effect sizes for ApoB (alternative)?

A Bayes factor (e.g., BF₁₀ = 6) allows a stronger statement:

“The observed data are 6 times more likely (moderate evidence) under the ‘no association’ model than under the alternative model that assumes some effect from ApoB (as defined by the prior).”

• Frequentist: “No evidence of effect”
  
• Bayesian: “Evidence for no effect”

Bayesian Prior: represents your belief about likely effect sizes before seeing the data.

From the BayesFactor documentation for the parameter rscaleCont:

“Several named values are recognized: ‘medium’, ‘wide’, and ‘ultrawide’, which correspond to rscales of √2/4, 1/2, and √2/2, respectively.”

• “medium” → rscale = √2 / 4 ≈ 0.354
• “wide” → rscale = 0.5
• “ultrawide” → rscale = √2 / 2 ≈ 0.707

rscale of 0.8 is wider than “ultrawide”. It is not a “moderately informative” prior. It’s actually a weakly informative or vague prior, placing most of its weight on large effects.

A moderately informative prior would typically correspond to “medium” (≈ 0.354) or “wide” (0.5), which place more mass on smaller effects.

The authors’ choice of rscale isn’t wrong, but their description of it is misleading.

Labeling an rscale = 0.8 prior as “moderately informative” or “conservative” downplays the fact that it assumes large effects, making small observed effects look unlikely under H₁ and inflating support for H₀.

Their choice of prior is subjective, influential, and not tested for robustness.

• The model expected large ApoB effects, so small observed effects are treated as evidence for no effect.

• Best practice is to run a sensitivity analysis, to see whether conclusions change with different priors.

2. Univariable Linear Models
   Each predictor tested separately (ApoB, LDL-C, age…)
   No confounder adjustment → biased, unreliable, low credibility estimates

3. Bayesian Inference
   Bayes inference used to support “no ApoB effect” & “plaque begets plaque”
   Applied atop unadjusted, structurally weak models → amplifies conclusions

4. Bayesian Prior Choice (rscale = 0.8)
   Prior assumes large effects
   No sensitivity analysis → results likely prior-driven

5. Bayes Factor Interpretation
   Claimed ApoB no association is “6–10× more likely…true”
   Bayes factor misstated as posterior probability → compares model fit, not truth

6. Headline claim
   “Plaque Begets Plaque, ApoB Does Not”
   Overstates evidence → undermined by methodological limitations, unadjusted modeling, and incomplete model reporting

ΔNCPV, their primary outcome, is a change score between two bounded, skewed measures.
Likely to produce non-normal residuals and heteroscedasticity (e.g., larger spread at higher baseline).

If smaller baseline values were also linked to larger increases,
this may reflect the effects of left-censoring and error asymmetry — not true biological acceleration.

These issues are clear in TPS, and may affect NCPV, but diagnostics are not shown.

OLS assumes homoscedastic, normal residuals
performance::check_model() was run — but no output provided

They could have considered methods to address this such as: Tobit regression, log(+1) transform, or robust regression

The authors conducted an apparent post hoc “sensitivity analyses” in two subgroups:

• High adherence (\(n = 56\)): >80% of \(\beta\)-hydroxybutyrate values ≥ 0.3 mmol/L
• High CVD risk (\(n = 28\)): MESA 10-year risk >5%

Without knowing if the subgroups are distinct, it’s hard to tell whether these findings confirm one another or simply re-analyze overlapping data — replication vs. redundancy.

The same individuals may be contributing to both sets of sensitivity analyses.

This limits interpretability and weakens claims of consistency across groups.

Results: “Sensitivity analyses… showed similar results to those just reported”.

Compared to the full sample, the high adherence group offers only anecdotal evidence for the null.

The group is heterogeneous (to downplay the pooled NCPV change), yet they ran univariable regressions and interpreted Bayes factors on that group.

If a group is too heterogeneous to report pooled outcomes, it is also too heterogeneous for pooled inferences about predictors or mechanisms.

If their CVD risk (e.g., plaque progression) is not coherent, then the category fails as a predictive or explanatory label.

All clinical populations are heterogeneous in risk.

In other words: With nearly all LMHRs showing plaque progression, a wide IQR (37.3 mm³) doesn’t indicate balanced variability—it reflects differing degrees of worsening.

This matters because:

• The outcome (ΔNCPV) shows high variability across individuals in the LMHR group.
• That inflates standard errors, weakens statistical power, and makes small observed effects more ambiguous.
• It calls for adjusted modeling to reduce noise and account for confounding, not pooled univariable regressions and Bayes factors interpreted as strong evidence.

From the response:

“Regarding the analytical points brought forward, we are aware of the relevance of linear assumptions to obtain accurate estimators. Since residual plot evaluation can also be subjective…”

Objective, quantitative statistical tests also exist for assessing model assumptions:

• Normality: Shapiro-Wilk test, Kolmogorov–Smirnov test, Q-Q plots (visual / quantitative)
• Homoscedasticity: Breusch–Pagan test, White test
• Influence / leverage: Cook’s distance, leverage plots (visual based on quantitative values)

The performance::check_model() function they cite automatically generates most of these checks.

It’s unclear why they wouldn’t include or reference the output.

“…we followed their suggestion and re-ran all models with robust linear regression…as expected, there were small differences with the published estimates, all models using robust regression were consistent with what was reported.”

No output, diagnostics, or model fit provided. We are asked to trust their assertion.

The SD of ΔNCPV (31.5 mm³), equal to its mean, was omitted from the original paper and reported in response to critique.

That high level of variation (“heterogeneity”) weakens power and makes all regression results less reliable — not just the null finding on ApoB.

“We completely agree our exploratory results (especially those suggesting a null association between plaque progression and ApoB) should be interpreted with caution”

“Moreover, our results are compatible with a causal role of ApoB in atherosclerosis, as we have openly acknowledged and supported in previous publications.”

“Plaque Begets Plaque, ApoB Does Not”

In that citation [7], Yoon et al. did perform t-tests on change scores, but their main conclusions relied on a random-effects repeated-measures multivariable regression model of follow-up CAC, adjusted for baseline plaque and clinical risk factors.

The paper did not report any univariable linear regression models.

“In retrospect, we might have chosen “Longitudinal Data from the KETO-CTA Study” as alternative phrasing to avoid misinterpretations.”

“misinterpretations”